Pages

Wednesday, April 04, 2012

On the importance of being wrong

Some years ago, I attended a seminar by a young postdoc who spoke about an extension of the standard model of particle physics. Known as “physics beyond the standard model,” this is a research area where theory is presently way ahead of experiment. In the hope to hit something by shooting in the dark, theorists add stuff that we haven’t seen to the stuff we know, and then explain why we haven’t seen the additional stuff – but might see it with some experiment which is about to deliver result. Ie, the theorists tell experimentalists where to look.

Due to the lack of observational evidence, the main guide in this research area is mathematical consistency combined with intuition. This type of research is absolutely necessary to make progress in the present situation, but it’s also very risky. Most of the models considered today will turn out to be wrong.

The content of the seminar wasn’t very memorable. The reason I still recall it is that, after the last slide had flashed by, somebody asked what the motivation is to consider this extension of the standard model, to which the speaker replied “There is none, except that it can be done.”

This is a remarkably honest answer, especially since it came from a young researcher who had still ahead of him the torturous road to tenure.

You don’t have to look far in the blogosphere or on Amazon to find unsolicited advice for researchers for how to sell themselves. There now exist coaching services for scientists, and some people make money writing books about “Marketing for Scientists.” None of them recommends that when you’ve come to the conclusion that a theory you looked at wasn’t as interesting as you might have thought, you go and actually say that. Heaven forbid: You’re supposed to be excited about the interesting results. You were right all along that the result would be important. And there are lots of motivations why this is the one and only right thing to do. You have won great insights in your research that are relevant for the future of mankind, at least, if not for all mankinds in all multiverses.

It’s advice well meant. It’s advice for how to reach your presumed personal goal of landing a permanent position in academia, taking into account the present mindset of your older peers. It is not advice for how to best benefit scientific research in the long run. In fact, unfortunately, the both goals can be in conflict.

Of course any researcher should in the first line work on something interesting, well motivated, and something that will deliver exciting results! But most often it doesn’t work as you wish it should. To help move science forward, the conclusion that the road you’ve been on doesn’t seem too promising should be published to prevent others from following you into a dead end, or at least telling them where the walls are. Say it, and start something new. It’s also important for your personal development. If you advertise your unexciting research as the greatest thing ever, you might eventually come to believe it and waste your whole life on it.

The reason nobody advises you to say your research project (which might not even have been your own choice) is unexciting is that it’s difficult if not impossible to publish a theoretical paper that examines an approach just to come to the conclusion that it’s not a particularly convincing description of nature. The problem with publishing negative results might be familiar to you from medicine, but it exists in theoretical physics as well. Even if you get it published, and even if it’s useful in saving others the time and work that you have invested, it will not create a research area and it’s unlikely to become well-cited. If that’s all you think matters, for what your career is concerned it would be a waste of your time indeed.

So, they are arguably right with their career advice. But as a scientist your task is to advance our understanding of nature, even if that means concluding you’ve wasted your time – and telling others about it. If you make everybody believe in the excitement of an implausible model, you risk getting stuck on a topic you don’t believe in. And, if you’re really successful, you get others stuck on it too. Congratulations.

This unexciting seminar speaker some years ago, and my own yawn, made me realize that we don’t value enough those who say: “I tried this and it was a mistake. I thought it was exciting, but I was wrong.” Basic research is a gamble. Failure is normal and being wrong is important.

20 comments:

If one has spent the time examining some idea, and has found out that it doesn't work, then of course, one cannot go about advertising the research as exciting. But the minimum one can get out of the time spent is a publication. I think people should value these almost like the no-go theorems. It is a marker that helps future researchers avoid dead ends.

The other value the researcher should have obtained from this work is expertise. And I think others should appreciate it in proportion to the difficulty and sophistication of what was attempted and found not to work.

I agree on everything. But I am afraid admitting one is wrong is not always a matter of whether you waste your time publishing it -- it is a matter of whether you want to kill your career (but I have disciplines other than theoretical physics in mind).

Unfortunately the inner workings of Academia right now are not optimized to encourage honesty very much.

Every research should be useful at least a bit for people outside of scientific community. Right here and right now. We have enough of "basic" research, which is just another term for well covered parasitism. We have enough of research topics, which are ignored for decades with mainstream physics and which could bring the practical applications soon. The players of strategical games like the Civilization or AgeOfEmpires know very well, it has no meaning to invest into development of "research items" in advance, because the energy exhausted in this way will not pay itself.

Father of String Theory and noted physics scientist Holger Bech Neilsen of Denmark has said that contributions from the Large Hadron Collider (LHC) at CERN are over-rated and that there is no need for spending so much on the experiment. Is the LHC throwing away too much data? I wouldn't further comment it, because my stance regarding the LHC research is quite known over the web (you know, all these foggy landscapes and water surface stuffs).

Bee: "Due to the lack of observational evidence, the main guide in this research area is mathematical consistency combined with intuition. This type of research is absolutely necessary to make progress in the present situation, but it’s also very risky."

I don't see how it is necessary, in fact I think that it is counterproductive.

The other approach where you first do experiments testing all the predictions of the current best model and only when a discrepancy is found you try to modify it is vastly superior - especially on economical grounds.

The only reason why this flawed way of doing research is popular is that there are plenty of theorists with nothing better to do.

Some may have applied a computerized technique to the synapse as a portal of the computer thinking mind? What of that relationship? Can computers think intuitively?Correlation of Cognition Think of Cognition and the idea of Tegmark as a mathematical universe?

In a comparative relation would one see such intuitive moments as part of distinctive classes as outline below?

Cognitivism has two major components, one methodological, the other theoretical

The question then about the inherent beginning of the universe is mathematical, how do such ideas arise from mathematicians? You see, Searle may push you to wonder about the computer as a logical sequence of events?:)

Yes, one gains expertise... The problem is that this sort of expertise doesn't spread very far. If it's not openly available there's a high risk others will waste time repeating mistakes, which is unnecessary. It's like there's a whole class of knowledge that's excluded from becoming openly available. Best,

Right, essentially what I was saying is that the inner workings of academia are not optimized to encourage honesty, you put that very well. That's a bad situation for science altogether. The very least we can do is remind people what's important for progress - and what isn't. You don't kill your career if you admit being wrong. You presently run a risk of it being killed by others, which represents a mindset among older scientists that can however change over time. Which disciplines did you have in mind? Best,

The costly part of physics is the experiment, not the theory. Theorists are cheap. The reason you need theories for physics beyond the standard model is that you better have a really good reason to build a costly experiment. There are many things you can look for, and we simply can't afford all of them.

If you don't do that, you end up with stuff like Craig Hogan's Holometer. He doesn't have a theory. He just has a hunch and a vague idea. And 2 Mio $. Now in the grand scheme of things, 2 Mio isn't that much, but that's not a procedure science can afford to use as a standard. Best,

A related issue is that papers which are a bit off the beaten path are often not cited, perhaps because people fear being associated with them. If the paper essentially says "we tried this and it didn't work; it isn't even interesting" then, OK, no citations are expected. On the other hand, if, to paraphrase Steve Martin, a wild and crazy paper comes along which a) addresses an important issue and b) is not obviously wrong, then folks producing more conventional papers should not be afraid to cite it. Sometimes, no-one cites it until some big cheese does, then all jump on the bandwagon.

Although one of the authors is a very distinguished scientist and knight of the realm, this paper, particular the abstract, demonstrates how it should be done:http://arxiv.org/abs/1110.2832 .

Yes... It's a story I know all too well. I've had many papers rejected for non-technical reasons, basically because some referee or editor was uncomfortable with me venturing "a bit off the beaten path." And that, I should add, still in a very conservative way. (I mean, look at my papers, it's not like I'm reinventing calculus. I just get easily bored.) This is terribly frustrating. If I'd get a report saying there's something wrong in Eq. (8), this would be bad enough, but at least I could work on it.

Leaving aside my own experience, what bothers me even more is that if I extrapolate it, it tells me just exactly why there isn't anything moving forward in this research area. And yes, I think the reason is exactly what you say: People don't have the time to think about it, and then they are afraid they might be associated with it. Ie, there's the editor who, when faced with a referee who dislikes a paper but can't come up with a technical reason, will reject the paper, rather than use his own brain or take a risk. Of course there are exceptions to this, but by and large this has been my experience. Best,

The fact that experiments are costly doesn't make wasting money on unproductive theorists ok. Besides what is also being wasted is intellectual capital, plenty of smart people spend their entire careers chasing rainbows, I bet it would be beneficial to society if they were instead directed to other more productive careers.

"The reason you need theories for physics beyond the standard model is that you better have a really good reason to build a costly experiment. There are many things you can look for, and we simply can't afford all of them. "

The problem with that argument is that the fact some completely unmotivated extension to SM predicts something is certainly NOT "a really good reason to build a costly experiment."

In fact unless LHC produces solid evidence of new physics which would need exploring I believe it should be the last in the succession of ever more expensive accelerators.

Finally can you provide an example of some important breakthrough in the history of physics which was discovered based on some completely unmotivated theory? All I can think of were motivated by experimental evidence or the need to simplify theory or improve it's self-consistency.

I agree with you more than you might think on the issue of chasing rainbows and wasting intellectual capital. I just see the origin of the problem elsewhere. The problem isn't that this type of research is per se entirely unnecessary. The problem is that we're doing it wrong. Of course one shouldn't waste money on unproductive research, whether theoretical nor experimental. What I'm saying is that, if done well, physics beyond the standard model increases the return on investment of experiments.

Btw, I think this problem is to a big extend socially created. There are just too many particle physicists with no data to bite their intellectual teeth into. Best,

One might contend that the mathematical basis of String Theory is outright wrong yet it was possible for it to push back perspective on the very beginnings of the universe? Ideas are cheap, while theoretically you have to provide for the framework..the meta-view is not easy?:)It takes work?

http://www.quantumdiaries.org/wp-content/uploads/2012/03/exclusion.png More data will falsify the last interval. Stop now!

http://418lab.chem.univ.kiev.ua/img/propellane.jpg [1.1.1]Propellane is "impossible." [2.1.1]propellane was photochemically diddled in a deep cryogenic matrix. A new grad student was sent on a snark hunt - large ring propellane synthesis using the small precursor. Product obtained in high yield with no special circumstances (symmetry footnote).

No predictive theory is wasted if 1) somebody reaches for a blue rose where it is not, and 2) management is busy elsewhere. Do opposite shoes (right-handed versus left-handed alpha-quartz or gamma-glycine single crystal test masses) violate the Equivalence Principle? Theories of mass have symmetry breakings because massless boson photons and massed fermions have measurably non-identical vacuum interactions. Somebody should look.

Bee, I couldn't agree more with what you said. I would even go one step further: sociology in physics now allows for intellectual snipers to prey on those with the temerity to offer a new intuitive and exciting idea that has not yet had an experiment tried to validate it. They would rather go with old, non-intuitive ideas (but exiting to them) that have no reasonable chance for experiment, and thus no chance to be proven wrong. Oh the humanity! :-)

It would be a very useful and potentially enlightening to identify expressly the fundamental assumptions that current physics is founded upon.

Then, the physics community could ask for each of these assumptions: "What if this assumption is wrong?".

The history of physics clearly shows that major breakthroughs result from some maverick ("crackpot" in today's parlance) questioning a fundamental assumption, like absolute space, time and simultaneity.

Why should not the whole physics community make more of an effort to question assumptions and consider different assumptions?RLODiscrete Scale Relativity

There might not be a systematic approach to that, but it's on many people's mind. I have been to numerous workshops where we had discussion sessions around exactly this topic: What are the assumptions. Which of these might we have to drop. Especially the issue of continuum vs discreteness receives a lot of attention. I personally am more interested in the quantization prescription. Then there's a lot of people who bash on different types of symmetries, Lorentz-invariance always among them. Some want to abandon unitary. Some locality. Some space, some time, some space and time. And so on and so forth. Best,

Chapter three of "Marketing for Scientists" does address this issue to some extent. It describes the importance of building long-term relationships with your customers--relationships that would falter if you regularly oversold your science.

And here's an interview from the marketing for scientists website with a former Congressman that also describes the importance of not overselling your scientific ideas and being able to deliver on your promises: